What Causes the Child Penalty? Evidence from Same
Sex Couples and Policy Reforms∗
Martin Andresen and Emily Nix
PRELIMINARY DRAFT - PLEASE DO NOT CITE OR CIRCULATE WITHOUT
PERMISSION FROM THE AUTHORS
Abstract
While the gender gap in income has narrowed over the past 50 years, women in hetero-
sexual couples continue to experience signi�cant labor market penalties following the birth
of children, while their partners experience no such penalty. This “relative child penalty” has
been well documented and accounts for the majority of the remaining gender gap in income
in many countries. A number of possible explanations for this relative child penalty exist:
gender norms around child care, di�erent preferences for child care among men and women,
e�cient specialization within households, and the impact of giving birth on women. In the
�rst half of this paper, we show that same sex couples do not experience the relative child
penalty in the same way as heterosexual couples. We develop a simple economic model that
incorporates the main explanations for the child penalty and generates testable predictions.
The model, combined with the empirical results, suggest that much of the child penalty expe-
rienced by women in heterosexual couples is due to gender norms and preferences, although
the costs of giving birth also contribute. Having established that the relative child penalty
in heterosexual couples is not inevitable and may not be e�cient, in the second half of the
paper we provide causal estimates on the impact of two policies aimed at reducing the child
penalty: paternity leave and improved access to child care. We �nd no signi�cant impact of
paternity leave on the relative child penalty. The analysis of improved access to child care is
in progress.
The gender gap has narrowed signi�cantly over the past 50 years.1
However, one component of
the gender gap has proven to be relatively persistent: the income penalty women in heterosexual
∗We thank Kenneth Aarskaug Wiik, Edwin Leuven, and Nina Drange.
1Economists have provided evidence on a number of explanations for this decline, such as the narrowing of the
gender education gap and the decrease in labor force discrimination.
1
couples experience after the birth of children. In contrast, men in heterosexual couples experience
no such income penalty upon the birth of children. This income penalty experienced by women is
called the “child penalty”2
and has been documented in a variety of countries such as the United
States, Denmark, Norway, and Sweden (see Chung et al. (2017), Kleven et al. (2018), Bergsvik
et al. (2018), and Angelov et al. (2016)). As other determinants of the gender gap have declined in
importance, the proportion of the gap that can be explained by the “relative child penalty”, the
di�erence in the child penalty experienced by fathers compared to mothers, has increased. Kleven
et al. (2018) show that in Denmark the relative child penalty accounts for 80% of the gender gap
in 2013, compared to 40% in 1980.
The stubborn persistence of the relative child penalty among heterosexual couples is a puz-
zle, particularly given the overall decline in gender wage gaps. If the relative child penalty is
largely driven by di�erences in preferences between men and women, the impact of giving birth,
or e�cient specialization within households, then the relative child penalty may be an optimal
response to the arrival of children. On the other hand, the relative child penalty could be caused
by persistent gender norms around child care which may be economically ine�cient. In addi-
tion to contributing to the gender gap, we also �nd that the arrival of children in heterosexual
couples causes a drop in overall household income. Does this drop represent a necessary cost to
households of having children?
To address these questions we estimate and compare the child penalties among same sex male
and same sex female partners to the child penalties experienced by heterosexual couples using
administrative data from Norway. Our approach is motivated by suggestive evidence that same
sex couples split household chores more evenly. If the absence of pre-set gender roles lead same
sex couples to also split the burden of child care more evenly, the child penalties may look very
di�erent among same sex couples. To identify the child penalties within each couple type, we
use an event study approach as in Kleven et al. (2018).
To more formally understand how our results can disentangle the roles of preferences, giving
2Although commonly called a “penalty”, this could very well be driven purely by preferences and not discrimi-
nation, which some may associate with the word penalty. This paper aims at disentangling these mechanisms, but
we will use the term “child penalty” for the income loss following child birth independently of the mechanism. This
is in line with the literature.
2
birth, household specialization and gender norms around child care in the heterosexual relative
child penalty, we build a simple model of the household’s labor supply before and after the arrival
of children. In the model, partners may di�er in their relative productivity in the labor market
versus home production, men and women may have di�erent preferences for child care, and preg-
nancy imposes a �xed cost to the woman physically bearing the child. We model gender norms
as a disutility for men in heterosexual couples from women working outside the home after the
child is born, as in Fernández et al. (2004). The model yields the following intuitive predictions. As
expected, and by construction, each of these mechanisms yield a relative child penalty for hetero-
sexual couples. If household specialization drives the relative child penalty within heterosexual
couples, the model predicts similar child penalty patterns in otherwise similar same sex couples.
If women have greater preferences for child care than men, the model predicts child penalties for
both partners in same sex female couples and smaller or no penalties for partners in same sex
male couples. If part of the relative child penalty is driven by the costs of giving birth, the model
predicts a relative child penalty for the pregnant mother versus the non-pregnant mother among
same sex female couples, but no such di�erential among same sex male partners. If gender norms
cause the relative child penalty in heterosexual couples, the model predicts that we will not �nd
relative child penalties among same sex couples.
Similar to previous papers, we �nd that women in heterosexual couples experience a drop
in income of approximately 22% following the birth of the �rst child, and this drop persists over
time. Their husbands experience no income penalty from children. For female same sex couples
we �nd an initial 13% drop in the income of the partner who gives birth. Her partner experiences
an initial income drop of 5%. Despite experiencing a larger immediate drop in income, the mother
who gives birth catches up with her partner around two years after birth, and from that point
on both mothers experience similarly sized child penalties which decrease over time, until there
is no longer a child penalty four years after birth. These patterns suggest that both biology and
female preferences play a role in the relative child penalty experienced by heterosexual couples,
but gender norms likely play a large role as well. While the population of same sex male couples
with children is very small, we �nd no income penalty for either spouse. This is also consistent
3
with a dominant gender norms and female preferences mechanism, and a smaller role played
by biology. In terms of total household income, we �nd that the drop is larger for heterosexual
couples compared to same sex female couples.
From a social planner’s perspective, if shared parenting has negative impacts on children, then
reducing the heterosexual relative child penalty might not be optimal even if much of the di�er-
ences in the child penalties experienced by heterosexual men and women is caused by gender
norms. We �nd that despite a lower overall household income penalty within same sex couples,
the children of same sex couples outperform children of heterosexual couples on English, reading
and math tests at age 10.
Thus, large and persistent di�erences in the child penalty within a couple are not inevitable,
and most of this gap is due to gender norms and women’s preferences. The evidence from the �rst
half of the paper helps us better understand the mechanisms behind the relative child penalty in
heterosexual couples, but it does not tell us what impact policy might have on the relative child
penalty. Policy makers might wish to know how to decrease the relative child penalty for two
reasons. First, decreasing the relative child penalty would almost certainly reduce the overall
gender income gap. Second, decreasing the relative child penalty could also improve welfare
more generally given our �ndings on household income and children’s test scores at age 10.
Broadly speaking there are two possible approaches to try and reduce the relative child penalty:
increase father participation in child rearing or provide support to mothers. Successful policies
targeting fathers would increase the child penalty for heterosexual fathers while decreasing the
child penalty for heterosexual mothers. Successful policies targeting mothers would decrease the
child penalty for heterosexual women as a result of the state serving as a “third partner” who
shares the burden of child rearing with women. These two approaches are very di�erent, and it
is not clear a priori which approach is best.
In the second half of this paper, we compare the impact of a policy targeting fathers on the
relative child penalty of heterosexual couples versus a policy targeting mothers. First, we esti-
mate the causal impact of paid paternity leave on the relative child penalty. We use a regression
discontinuity design to estimate the impact of 6 di�erent expansions of the paid paternity leave
4
quota in Norway from 1993 to 2013. We estimate a strong �rst stage: the reforms signi�cantly
increased the amount of paternity leave that fathers take. However, we �nd no signi�cant impact
on the relative child penalty. Our results are consistent with Antecol et al. (2016) who �nd that
gender neutral tenure clock stopping policies do not help academic women, and may even hurt
their careers. We examine a similar shift toward more gender neutral leave policies, and �nd that
they do not help women across the population of professions in Norway.
Next, we estimate the causal impact of a 2002 reform that greatly increased the funding pro-
vided for formal child care, with signi�cant variation in the timing of the expansion across mu-
nicipalities. We use the same IV strategy developed in Andresen and Havnes (2018), but look
speci�cally at the relative child penalty. [IN PROGRESS].
Our paper is most closely related to the literature on child penalties. We use the simple event
study approach used in Chung et al. (2017), Kleven et al. (2018), Bergsvik et al. (2018), and Angelov
et al. (2016) to identify child penalties across couple types. Together, our results and the results
from these papers make clear two facts. First, there does not appear to be a sample of heterosexual
couples, whether in di�erent countries, educational groups, or socioeconomic class, that does not
experience large relative child penalties. Second, the child penalty has become the most important
driver of gender gaps. However, by using same sex couples as a comparison, our paper contributes
more substantially to this literature by shedding light on why the relative child penalty exists,
which is di�cult to surmise by looking only at heterosexual couples. Related to our results,
Kuziemko et al. (2018) also �nd evidence that preferences of heterosexual women may play an
important role in the child penalty. Speci�cally, they show that women in heterosexual couples
exhibit time inconsistency in these preferences, �nding that the women report more negative
opinions toward female employment after giving birth relative to before birth.
We also contribute to a small body of evidence on same sex couples with children. While com-
paring the outcomes of children born to same sex and heterosexual couples is not the focus of this
paper, this topic has been a major point of controversy in the United States and elsewhere. In the
landmark 2015 Supreme Court case Obergefell v. Hodges, which legalized same sex marriage, the
well being of children was a central theme in oral arguments. Justice Scalia raised a concern that
5
not all studies conclude children of same sex parents fare equally well. The empirical evidence
has been limited and mostly based in the �elds of sociology and psychology. Previous studies of
children born to same sex couples have been criticized by both sides of the debate on the basis of
three methodological concerns: non-representative samples3, mislabeling children from hetero-
sexual couples as children of homosexual couples or vice versa4, and small sample size. In this
paper, our use of administrative data containing the population of children of same sex couples
in Norway and the ability to identify such children accurately largely overcomes these concerns.
While the population of children born to same sex couples in our sample years is modest when
compared to the population of children born to heterosexual couples, it is much larger than the
vast majority of existing studies. We �nd that same sex couples are di�erent from heterosexual
couples in terms of observables before birth, so when estimating the impact of having same sex
parents on test scores at age 10 we control for income, age, education and other factors that could
a�ect child outcomes (the results are stronger without these controls). We �nd no evidence of
adverse schooling outcomes for children of same sex parents. On the contrary, we �nd that chil-
dren of same sex (mostly lesbian) couples have higher math, English, and reading scores at age
10, and the e�ect is signi�cant at the 99th percentile for English and reading scores.
The remainder of the paper is organized as follows. In Section 2 we present a model for
household production of children and derive testable predictions. In Section 3 we describe our
approach to identify child penalties across couple types. In Section 4 we outline the institutional
background and the data, and in Section 5 we present the main results. Having established that
the child penalty is not inevitable, in Section 6 we analyze the impact of paternity leave and access
to better child care on the heterosexual child penalty. In Section 7 we conclude.
3Studies often used “opportunity samples” where couples volunteer to participate.
4In particular, a number of studies label children born to a heterosexual couple, which later divorces and one
spouse enters a same sex relationship, as children of homosexual couples. Under this approach, if these children
do worse than children in stable heterosexual couples, it is impossible to disentangle the impact of divorce versus
having one set of same sex parents.
6
1 A model of household labor supply in the presence of of children
In this section we develop and solve a simple household model. The model includes the most
commonly suggested mechanisms for the child penalty: gender norms around child care, spe-
cialization within households, preferences, and the impact of giving birth. The solutions of the
model provide testable predictions that we bring to the data. Our model is loosely adapted from
similar household models in Fernández et al. (2004) and Olivetti (2006).
There are three periods. In the �rst period, households consist of two adults. In the second
period, the child arrives in the household (either adopted or birthed by a female adult).5
In the
third period, the household consists of the two adults and the child. Each adult is endowed with
1 unit of time in every period. In the �rst period there is no child and no home production, so
all adults supply their unit of time inelastically to the market. In the second and third period,
households choose the amount of labor each adult allocates between home and labor market
production. The two adults may be of any gender (man and women, two men, or two women).
The quasi linear utility function of each spouse i ∈ a, b is given by:
Ui (c, θ, t−i) = c+ β ln θ + η ln (1− tb) Xi − αt−iZi
where c is consumption and θ is child quality (ln θ is equal to zero in the �rst period). Zi is an
indicator equal to 1 if the individual is a male married to a female in periods 2 and 3, and Xi is an
indicator equal to 1 if the individual is female. β represents the value of child quality and η is the
additional utility women get from being at home with children, capturing potential di�erences
in gender preferences over time with children. α is the disutility men get from each hour their
wife works when they have children, capturing gender norms around child care.6
5We do not model the fertility decision or allow parents to make labor market decisions in anticipation of chil-
dren. While these are important issues (see for example Bursztyn et al. (2017)), they are beyond the scope of this
paper. We do allow for an income gap before children, which could capture some of these points.
6Survey evidence shows large di�erences in the norms towards working women with young children compared
to working women without children. As an example, 80 % of the respondents in the ISSP in 2002 think that married
women without children should work full time in the US, while only around 15% think the same about women
with children below school age. Similar di�erences appear for other countries, including Sweden and Denmark, see
International Social Survey Program (ISSP) from 2002.
7
There is no saving or borrowing, and in each period household consumption is joint and equal
to the sum of spouses’ earnings. For simplicity, we do not model wage setting, and simply take
as given the wages of each spouse wa and wb, so that
c = wata + wb
(1− δS
)tb
where S is an indicator equal to 1 in the second period if the spouse is a woman who gave birth,
and δ is the labor market cost of giving birth. We represent total income of each individual in
each period as Yi = witi.
Child quality is produced by the following production function
P = kah (1− ta) + kbh (1− tb)
where ki ≥ 0 are productivity parameters, h′> 0, h
′′ ≤ 0, and h (0) = 0.
The household maximizes utility by choosing each spouse’s division of labor in periods 2 and
3, where household utility is given by
∑i
λiUi (c, θ, t−i)
and λi is the weight of each spouse in household decisions. This assumes Pareto e�ciency in
household decisions and is consistent with a number of household bargaining problems.7
Notice
that we assume that the bargaining weights do not vary by couple type. An alternative approach
to capture gender norms could be to assume that in same sex couples λa = λb and in heterosexual
couples λa > λb, where λa represents the Pareto weight of the man. In the appendix, we show
that this approach yields similar predictions to the current model.
There are no dynamics to the problem. This means we can solve the problem sequentially,
maximizing ta and tb in each period. In period 1, ta = tb = 1 by assumption. For periods 2 and 3,
7This is a very simple model by design. It assumes Pareto e�ciency, but this has some important drawbacks.
See Del Boca and Flinn (2012) for a discussion of alternative approaches.
8
the couples solve:
maxta,tb
(λa + λb)(wata + wbtb − δwbtbS + β ln θ
)+λaη ln (1− ta) Xa+λbη ln (1− tb) Xb−λaαtbZa
(1)
The �rst order conditions for the second period are given below. The �rst order conditions for
the third period are identical, except δ = 0.
wa
ka=
βh′(1− ta)
kah (1− ta) + kbh (1− tb)+
λaηXa
ka (λa + λb) (1− ta)(1− δ)wb
kb=
βh′(1− tb)
kah (1− ta) + kbh (1− tb)+
λaαZa
kb (λa + λb)+
λbηXb
kb (λa + λb) (1− tb)(2)
Equations 2 yield the following predictions:
1. Preferences: The income penalty is increasing for all women as η increases. The income
penalty for heterosexual men is decreasing. However, for any given η > 0, the increase in
the income penalty experienced by lesbian women due to an increase in η is smaller than
the increase in the income penalty for heterosexual women. The relative child penalty for
heterosexual couples is increasing in η at an increasing rate if h′′< 0 and at a constant rate
otherwise. The child penalty for lesbian couples is zero if δ = wa
ka− wb
kb= 0. Otherwise,
there is no contribution to any existing relative child penalty for lesbian couples so long as
h′′
is constant. By construction, η has no impact on the incomes of gay men, and cannot
account for a relative child penalty for gay men.
2. Biology: The income penalty is increasing for the women who gives birth as δ increases,
but only in period 2 (the income penalty is decreasing for her partner). The relative child
penalty in period 2 for lesbian and heterosexual couples is increasing in δ at an increasing
rate if h′′< 0 and at a constant rate otherwise. δ has no impact on the income or relative
child penalty of gay men by construction.
3. Gender norms: The income penalty for heterosexual women is increasing as α increases
(and the income penalty for heterosexual men is decreasing). The relative child penalty for
9
Table 1: Summary of the predictions of the model
Individual Child Penalty
Heterosexual Lesbian Gay
Preferences (η) Female spouse Both spouses (<hetero) Neither spouse
Biology (α) Female spouse One spouse Neither spouse
Gender norms(δ) Female spouse Neither spouse Neither spouse
Specialization (wa
ka− wb
kb) Female spouse One spouse One spouse
Relative Child Penalty
Heterosexual Lesbian Gay
Preferences (η) Yes No No
Biology (α) Yes; Period 2 only Yes; Period 2 only No
Gender norms (δ) Yes No No
Specialization (wa
ka− wb
kb) Yes Yes Yes
heterosexual couples is increasing in α at an increasing rate if h′′< 0 and at a constant rate
otherwise. By construction, η has no impact on the income and relative child penalties of
gay and lesbian women.
4. Intra-household Specialization: Let spouse a have a comparative advantage in market
work, so thatwa
ka≥ wb
kb. The income penalty for spouse a is decreasing as
wa
ka− wb
kbincreases,
while the income penalty for spouse b is increasing aswa
ka− wb
kbincreases. The relative child
penalty for heterosexual, lesbian, and gay couples is increasing aswa
ka− wb
kbincreases.
We also capture the predictions of the model for period 2 income penalties and within couple
relative child penalties graphically in Figure 1. Figure 1 plots the child penalty, the percentage
change in income relative to the �rst period of each couple on the left hand side and the relative
child penalty, the di�erence between the child penalties of spouse a and b on the right hand side,
based on the time allocations that maximize equation 1 as we vary each parameter (η, δ, α, and
10
wa) individually. Note that period 3 graphs are identical, except there is no longer a biological
penalty.
Every mechanism leads to a child penalty for that di�ers between mothers and fathers in
heterosexual couples, which is why it is so hard to disentangle mechanisms when looking only
at heterosexual couples. Adding same sex couples allows us to distinguish between mechanisms.
While the simulations show the impact of each mechanism separately, the general predictions of
the model hold for any combination of parameter values. Based on the model, we can rule out
specialization if we compare similar couple types in terms of market and household productivity
if we don’t also see a relative child penalty for lesbian and gay couples in periods 2 and 3. Biology
plays a role if we see an income penalty for the woman giving birth and a relative child penalty for
lesbian and heterosexual couples in period 2, but not in period 3 for lesbian couples. We can rule
out preferences if we don’t see an income penalty for both women in same sex female couples.
Perhaps the most surprising result that comes out of the model is the fact that the child penal-
ties for lesbian women due to female preferences will be smaller than the child penalty for hetero-
sexual women, which can also be seen in Figure 1. The intuition is that in heterosexual couples,
the husband will decrease labor supply less to compensate for lost income from the mother, while
in lesbian couples both spouses will do some of this compensation. This will be an important
caveat for our results, and it will be key to understand how much the income penalties might
di�er in the third period if α = 0.
2 Empirical strategy
To bring the model predictions to the data, we must �rst identify child penalties across couple
types. To identify the child penalty for each partner in each couple type we adopt an event-study
framework as in Kleven et al. (2018). The choice to have children is potentially endogenous to
many other determinants of income. However, if children impact a given labor market outcome
of interest such as income, then the precise year in which the child arrives will correspond to a
sharp discontinuity in income. Provided the other determinants of income do not also experience
sharp changes when the child arrives, we can attribute the corresponding discontinuity in income
11
12
Figure 1: Model Predictions: Simulations for Preferences and Biology
Note: Left panels show individual income penalties relative to full time income in period 1, and right panels show
child penalty by couple type. To produce the simulations we set h(1− ti) = 1− ti. The baseline parameter values
are: ka = kb = 1, λa = λb = .5, and β = 5. At baseline, wages of both partners are normally distributed with
mean 10 and standard deviation 1. At baseline α = η = δ = 0. In panel 1, we solve for 100 equally spaced grid
points of η ∈ [0, 40], keeping all other values �xed. Similarly, in panel 2, we solve for δ ∈ [0, 1].
13
Figure 2: Model Predictions: Simulations for Gender Norms and Specialization
Note: Left panels show individual income penalties relative to full time income in period 1, and right panels show
child penalty by couple type. To produce the simulations we set h(1− ti) = 1− ti. The baseline parameter values
are: ka = kb = 1, λa = λb = .5, and β = 5. At baseline, wages of both partners are normally distributed with
mean 10 and standard deviation 1. At baseline α = η = δ = 0. In panel 1, we solve for 100 equally spaced grid
points of α ∈ [0, 40]. In the last panel, we vary the mean of wa between 10 and 30.
to the arrival of children.
This suggests a simple regression of the outcome of interest on event time dummies. For our
main results we also include gender speci�c age and year dummies which control �exibly for
life-cycle and time trends in income. The results with only event time dummies are included in
Figure 13 in the Appendix and are very similar, but Kleven et al. (2018) show that including age
and time dummies performs better in identifying child penalties. More formally, let t represent
event year, with t = 0 corresponding to the year in which the couple’s �rst child is born. Let yit
be the labor market outcome of interest for individual i at event time t. We estimate the following
equation to identify the child penalty:
yit =
Parent-type-speci�c event time dummies︷ ︸︸ ︷∑j 6=−1
∑k
αjk1[t = j,Ki = k] +
Gender- speci�c age pro�le︷ ︸︸ ︷∑l
∑m
βlm1[ageit = l, Xi = m]
+∑n
∑o
γno1[Tit = n,Gi = o]︸ ︷︷ ︸Gender-speci�c calendar year shocks
+∑p
ηp1[Ki = p]︸ ︷︷ ︸Parent-type speci�c �xed e�ects
+εit (3)
Where Xi is the gender (male, female) of parent i, ageit is the age of parent i at event time t, Tit
is the calendar year for individual i at event time t, and Ki is the parent type: mother or father in
heterosexual couple, mother or co-mother in a lesbian couple, father or co-father in a gay couple.
1[A] is the indicator function for event A. Standard errors are clustered by couple and robust
to heteroskedasticity. The event time dummy the year before birth is omitted, which implies
that all estimates of event dummies are relative to the year before birth. Note that while we
allow life-cycle and time trends to vary by gender, we do not allow them to di�er within gender.
This means that the e�ect of age and year on income do not depend on whether a woman in a
lesbian couple is registered as the primary mother or the co-mother. Equation 3 is equivalent
to running the regressions separately for mothers and father if we only estimate the equation
for heterosexual couples.8
Notice that all parents in our sample eventually have children, so that
8While it is possible to estimate equation 3 separately for heterosexual mothers and fathers, lesbian mothers and
co-mothers and gay fathers and co-fathers, estimating the equation jointly allows us to exploit the large number of
heterosexual couples to help identify these controls for the same-sex couples as well as heterosexual couples.
14
the event dummies are identi�ed from comparisons of parents with a youngest child aged j to
parents of children at other ages in the same calendar year. Thus, if the exact timing of birth is
as good as randomly assigned conditional on gender-speci�c year and calendar-�xed e�ects, our
estimates can be given a causal interpretation as the impact of children on earnings. Kleven et al.
(2018) show that the event study approach we use here performs well at identifying both short
and long run child penalties compared to alternative approaches such as using instruments for
�rst birth.
Our objects of interest are αjk, the change in the outcome for a parent of type k at child age
j compared to the earnings the year before birth. Ideally, we would use a log-linear speci�cation
of equation 3 so that we could interpret the coe�cients as percentage change in earnings, but
the presence of zeros in the outcome complicates matters. To convert these absolute estimates to
percentage child penalties, we follow Kleven et al. (2018) and construct the following measure of
the child penalty.
Cjk =αjk
E(y | t = j,Ki = k)(4)
The interpretation of Cjk is the percentage drop in the outcome for parent type k at child age
j relative to the predicted outcome absent children. As an alternative, we also construct
Pj =αj2 − αj1
E(yit | t = j,Ki = 1)(5)
which is a measure of the relative child penalty of mothers relative to men in heterosexual couples,
in percentages of the predicted wages of mothers in the absence of children. Notice that spouse
typeKi = 1 denotes mothers in heterosexual couples andKi = 2 denotes fathers in heterosexual
couples. When computing con�dence intervals or standard errors for these estimates, we use
cluster bootstrap to account for the fact that the denominator is an estimated object.
15
2.1 Comparing heterosexual and same sex couples
If the exact timing of births is as good as randomly assigned conditional on gender-speci�c age
pro�les and yearly shocks, the simple event study identi�es the causal e�ect of having children on
labor market outcomes of mothers and fathers in heterosexual couples, mothers and co-mothers
in lesbian couples, and fathers and co-fathers in gay couples. These results are interesting on
their own, so we highlight them below. However, any di�erences across couples types are only
informative regarding the cause of the heterosexual child penalty if the distribution ofwa
ka− wb
kb
is identical across couple types, according to our model. If the distributions are not identical, we
can control for specialization in the event study by estimating:
yit =
Parent-type-speci�c event time dummies︷ ︸︸ ︷∑j 6=−1
∑k
αjk1[t = j,Ki = k] +
time dummies interacted with relative productivity di�erence︷ ︸︸ ︷∑j 6=−1
θj1[t = j]
(wi
ki− w−ik−i
)
+
Gender- speci�c age pro�le︷ ︸︸ ︷∑l
∑m
βlm1[ageit = l, Gi = m] +∑n
∑o
γno1[Tit = n,Gi = o]︸ ︷︷ ︸Gender-speci�c calendar year shocks
(6)
+∑p
ηp1[Ki = p]︸ ︷︷ ︸Parent-type speci�c �xed e�ects
+εit (7)
We observe pre-child income, Ia and Ib. We do not observe productivity in home production
(ka, kb). However, Ia − Ib is su�cient if ka = kb, or if one of the following conditions hold.
First, consider a more general model where there is household production before and after the
child arrives. In that case, specialization will occur before the child arrives and will be captured
by pre-market income gaps. Provided the household productivity parameters are unchanged or
linearly related over time, then Ia−Ib controls forwa
ka− wb
kb. Second, if k is instead identical for all
women and smaller than k for all men (for example, women do more household chores as girls
then men), then controlling for Ia − Ib should also be su�cient.
We use two approaches to control for pre-birth comparative advantage in market work. First,
16
we �exibly control for the di�erences in own and spouse’s earnings either the year before birth
or four years prior to birth interacted with event dummies, by estimating equation 7, replacing
wa
ka− wb
kbwith Ia−Ib. To the extent that comparative advantage is captured by the relative income
levels of the two spouses, these �exible controls will pick it up and we can attribute the remaining
child penalties from αjk to the other possible mechanisms highlighted by the model. Second,
in case the (untestable) assumptions required for the �rst approach to work do not hold, we
also report results using propensity score matching to construct samples of heterosexual couples
that are identical to either lesbian or gay couples based on observables. Using this approach,
we re-estimate equation 3 using the weighted sample of matching heterosexual couples. In our
matching results we control for the following variables: own income at event time -1, income
of partner at even time -1, age, gender, own and partner’s education, and year [IN PROGRESS].
As before, we scale our estimates by the predicted earnings in the absence of children. Notice
that this means that we will plot the partial, or unexplained by comparative advantage, portion
of the child penalties when controlling for comparative advantage as a fraction of earnings in the
absence of children.
3 Institutional context, data and sample selection
Norway was the second country in the world to legally recognize same-sex partnerships in 1993
through the Partnership Act, and Figure 3 documents the number of new same sex male and
female partnerships in Norway following the Partnership Act.9
Under this act, a partnership
was legally equivalent to marriage in most respects. However, the partnerships were restricted
regarding children. Same sex couples were not eligible for adoptions within country, were not
eligible for publicly subsidized assisted fertility treatment, and the registered spouse of a woman
giving birth was not automatically registered as the second parent (as the pater est principle
implements for married heterosexual couples). It wasn’t until 2002 that a change to the rules for
adoptions allowed same-sex couples to formally adopt the children of their spouse. The change
to the guidelines allowed same-sex couples to be considered for adoption of stepchildren just like
9Aarskaug Wiik et al. (2014) investigates the stability of these same sex marriages and partnerships.
17
marriages −><− partnerships
50
100
150
200
250
1993 1995 1997 1999 2001 2003 2005 2007 2009 2011 2013 2015 2017
Men Women
Figure 3: Number of new same-sex partnerships and marriages in Norway, 1993-2017
Source: Statistics Norway Statistikkbanken, tables 10160 and 05713.
heterosexual couples. The guidelines required a stable relationship and having had a de facto
parenting role for the child in question for some period of time, most often 5 years, as well as
consent from the existing legal parent. If the child was already registered with two parents,
the other parent was given the right to express his opinion on the adoption, but the case was
ultimately decided by the adoption agency.
In practice the increasing use and availability of assisted fertility treatments among lesbian
couples challenged this 5-year rule, as planned children of lesbian couples conceived through
assisted fertilization abroad became increasingly common. Therefore, in 2006 the Norwegian
government clari�ed the rules so that the 5-year rule would not apply in cases where the father-
hood cannot be established, such as with IVF treatment using an anonymous donor. In 2009, a
new marriage act was introduced which equalized same-sex and heterosexual marriages in all
but one respect: a same-sex spouse cannot later adopt the child of his/her spouse that was in turn
adopted from a country that does not allow adoptions to same-sex couples. The new marriage
law in 2009 also gave lesbian couples the right to IVF treatment in Norway, but only when us-
18
ing non-anonymous donor, as the law requires all children conceived through IVF to have the
possibility of knowing the identity of the donor father at age 18. Before this, lesbian couples
often traveled abroad to get IVF treatment, most often in Denmark. Even after the new law was
passed, many couples still travel abroad either to speed up the process or because they want to
use an anonymous donor. If conception happens through IVF treatment with a non-anonymous
donor in a recognized (private or public) fertility clinic, co-mothership can now be registered at
birth, but otherwise the couple must go through an adoption process in order for the partner to
be formally registered as the co-mother.
For gay couples, getting children is naturally more complicated. Surrogacy is illegal in Nor-
way, but some gay couples still enter into surrogacy agreements with surrogate mothers from
abroad. No special rules apply to these children, and parenthood must be established according
to the law when returning with the child. Typically, this means that the (most often biological)
father will declare fatherhood upon returning to Norway and be registered as the father, and
that the other spouse will then have to start the adoption process to be registered as co-father.
Alternatively, gay and lesbian couples have formally been eligible for adoption since 2009 just
like heterosexual couples, but this possibility is typically limited by the lack of donor countries
willing to adopt children to these couples.10
Domestic adoption at birth is very rare in Norway,11
but some children are adopted by their foster parents after a number of years in foster care. This
typically happens at much later ages and we would not expect this to have an impact on labor
market status around the birth of the child.
We do not observe births or adoptions directly, only registrations of legal parent status in the
population registers. In practice, we therefore observe children appearing in same-sex couples at
various times following birth. When identifying births to same sex couples in the administrative
10The �rst adoption from abroad to a same-sex couple in Norway happened in the fall of 2017. Colombia became
the �rst donor country to approve an adoption to a Norwegian same-sex couple, following a controversial Supreme
Court ruling from 2015. In the empirical analysis, we restrict attention to children born in 2013 at the latest, so that
foreign adoptions to same-sex couples should not be a relevant option.
11Ruling out adoptions by near family and adoptions of foster- and step-children, as few as two to three children
are adopted away at birth or right after per year in Norway. In addition, the biological parents are given a say
on prospective adoptive parents, and their opinion is given considerable weight in the decision among potential
adoptive parents. This makes matters worse for same-sex couples if the biological mother prefers a heterosexual
couple. In practice, this means that this option is not very relevant for same-sex couples, either.
19
05
01
00
15
02
00
nu
mb
er
of
ch
ildre
n
2002 2004 2006 2008 2010 2012 2014 2016year of birth
0 1 2 3 4+
age at adoption
(a) Lesbian couples
05
10
15
20
nu
mb
er
of
ch
ildre
n
2002 2004 2006 2008 2010 2012 2014 2016year of birth
0 1 2 3 4+
age at adoption
(b) Gay couples
Figure 4: Registered children to same-sex couples, by year of birth and age at adoption
Own calculations, based on sample and data described in section3. Age at adoption refers to the age of the child in
the year we �rst observe both parents registered
data, we try to be as certain as possible that we capture planned arrivals of children by a same-
sex couple that happens in the year of birth of the child, without losing too many observations
because children often aren’t legally registered until the following year.
3.1 Data and sample selection
Our data comes from Norwegian administrative registers covering the entire resident population.
Through unique identi�ers we link individuals over time and to family members such as parents,
enabling us to identify couples around the time of arrival of a child. Data on residency status,
date of birth, gender, municipality of residence and links to mother and father comes from the
o�cial population register, and is provided on January 1st every year from 2000 onwards. We
also have access to a permanent �le of links between children and parents, including all residents
ever registered in Norway as of 2016. We obtain data on education for years 1980-2016 from
o�cial education registers on the level, �eld and length of education as well as whether or not an
individual is enrolled in a study program by October 1st each year. Our labor market outcomes are
from two sources. The primary data on annual labor market earnings comes from the tax records.
20
We also observe the primary employment spell as measured in the matched employer-employee
register. This covers all public sector jobs and a large majority of jobs in the private sector, and
allow us to link individuals to their primary employer. Contracted hours are provided in bracketed
intervals only: from 4-19 hours a week, from 20 to 29 hours a week, or above 30 hours a week.
No information on wages is reported in the matched employer-employee register. Starting from
2015, the matched employer-employee register was replaced with detailed and precise data on
actual hours and wages based on monthly reports from the employers, called A-ordningen. We
utilize these unique data for some of the analysis. For parental leave and sickness absence spells,
we pull data from FD-Trygd, the register of the Norwegian Public Insurance system that provides
parental leave bene�ts.
We construct two main samples which we use throughout the empirical speci�cations. For
the long sample we start with all children born 1971 to 2010 where both mother and father are reg-
istered. We restrict attention to �rst-born children of both parents, and in case of multiple births
we include the parents only once. We drop a small number of couples where one of the parents
(most often the father) had several children with di�erent people in the same year. Unfortunately,
we do not observe residency status or changes of legal parent status before the year 2000, which
means that we may be allocating a very small number of later adoptees to their adoptive parents
even before the adoption happens.
For our main sample of same-sex and heterosexual couples, we want to be as certain as pos-
sible that we capture the arrival of planned children in a household with two parents. This is
more challenging given that the formal adoption process to the other parent in some cases may
take time.We therefore start with the universe of children born in Norway in the years 2001-2013.
We assign the parents to be the �rst parents ever registered to the child, which gives us a large
number of heterosexual parents and a small number of same sex parents.. This approach allows
for one of the parents to be missing for a year or two until the legal adoption procedure is com-
pleted. We restrict attention to children where both parents were legally registered as parents
at the latest in the year the child turns 3 in order to minimize the risk of capturing partners not
present at birth, and also to avoid getting an unbalanced sample of children even in the year of
21
birth. We furthermore keep only �rst-born children to both parents. In case of multiple births,
we keep the couple in the sample only once. We drop a handful of gay and lesbian couples who
gets multiple kids in the same year and register di�erent parent status for each child. Lastly, we
keep in both samples only couples where the �rst child appears at ages 22 to 60 for both parents,
giving us some time before and after birth to observe earnings.
This leaves us with a main sample of 231,200 heterosexual couples, 535 lesbian couples and
29 gay couples, and a long sample of 721,291 heterosexual couples. We match these mothers and
fathers to their labor market earnings and primary employment relation in all years from t − 4
to t + 15, centered around the birth of the �rst child, to investigate labor market response to
child birth. Note that for children born after 2001, we will not see a full 15 years of income after
birth because our data ends in 2016. Since most children born to same sex couples are born after
2001, we see later labor market outcomes much less frequently for same sex couples relative to
heterosexual couples. For the main sample we therefore restrict the window of interest to be
between t − 4 and t + 5 to limit this imbalance. Summary statistics for these samples are given
in table 2. The population of lesbian couples is reasonably large. In contrast, the number of
gay couples with children is very small, which corresponds to very imprecise estimates for this
group in the next section. As expected, the population of heterosexual couples with children is
very large.
We can also see that same sex couples have much higher pre-birth labor earnings relative to
heterosexual couples. This suggests that it will be very important to �exibly control for income
and initial income gaps in order to compare the child penalty between similar heterosexual, les-
bian and gay couples. Lesbian couples are slightly older than heterosexual couples at �rst birth,
and are also slightly more educated. Re�ecting the rules on establishing legal co-parent status,
the age at adoption is slightly delayed for lesbian couples compared to heterosexual couples (it
takes some time for the co-mother to be legally registered in some cases).
22
23
Table 2: Summary statistics by couple type
Heterosexual couples Lesbian couples Gay couples
Long sample Main sample Main sample Main sample
Birth year (�rst child) 1971-2010 2001-2013 2001-2013 2001-2013
A: Child characteristics
Birth year 1992.0 2007.2 2010.1 2011.7
(11.5) (3.72) (2.72) (1.52)
Multiple birth 0.015 0.020 0.071 0.24
(0.12) (0.14) (0.26) (0.44)
Female child 0.49 0.49 0.47 0.52
(0.50) (0.50) (0.49) (0.49)
Age at adoption 0.022 0.56 1.45
(0.17) (0.86) (0.91)
B: Parent characteristics, year before birth
Mother Father Mother Father Mother Co-mother Father Co-father
Parent type (K) 1 2 1 2 3 4 5 6
Age at �rst birth 26.3 28.7 27.8 30.2 32.3 32.8 38.5 38.6
(4.04) (4.83) (4.22) (4.98) (4.14) (5.72) (5.36) (6.21)
Labor earnings (1,000s) 250.3 346.3 343.5 473.2 481.8 476.7 744.6 837.4
(2017 NOK) (152.4) (243.6) (196.3) (319.3) (193.3) (317.7) (275.3) (386.4)
Years of education†
14.2 14.0 15.2 14.5 16.4 16.0 17.3 17.4
(2.94) (3.00) (2.88) (2.99) (2.42) (2.60) (2.42) (2.46)
N couples 721,291 231,200 535 29
Note: Summary statistics on estimation samples constructed as described in section 3. Standard deviations in
parentheses.†Available from 1980 and onwards only.
4 Main Results
In Figure 3 we present the main results. For each couple type, we present two graphs. The
�rst graph reports raw child penalties. The second graph reports estimates of Cjk (see equation
4) generated by the simple event study in equation 3. The results for heterosexual couples are
shown in the �rst row. As has been shown in so many other papers, we also �nd that mothers in
heterosexual couples experience large income penalties upon the birth of their �rst child while
fathers experience no income penalty.
The next row of graphs, corresponding to lesbian couples, is strikingly di�erent. We �nd that
both women experience a child penalty the year after the child is born, but initially the woman
who gives birth has a child penalty double the size of her partner. However, 2 years after birth the
woman who gives birth catches up and her penalty is no longer statistically signi�cantly di�erent
than her partner’s. By �ve years after birth, the child penalty both women experience has largely
disappeared.
The fact that the lesbian partner who gives birth initially experiences a larger child penalty
suggests that biology plays a role in the child penalty for heterosexual couples, but only in the �rst
year after birth. The fact that both partners experience child penalties, and that those penalties
are statistically indistinguishable from 2 years after birth onwards, suggest that women do have
a preference for children over career. Note that an alternative formulation of the model might
assume that η is larger for the mother who gives birth within a lesbian couple than the mother
who does not, given that which mother gives birth is endogenous in lesbian couples. However,
if this is the case then we would expect to see a persistent gap between lesbian mothers in both
periods, which is not what we �nd.
The last row of graphs correspond to gay couples. Consistent with the small population size,
the estimates are very imprecise. However, the patterns are consistent with a gender norms,
preferences, and biology story. In the event study, neither partner experiences a child penalty.
These results are suggestive, but without removing the contribution of specialization we can-
not de�nitively pinpoint mechanisms since the impact of specialization might di�er across couple
24
25
20
03
00
40
05
00
60
0A
nn
ua
l la
bo
r e
arn
ing
s in
1,0
00
NO
K
−4 −3 −2 −1 0 1 2 3 4 5Age of first child
Mothers Fathers
(a) Heterosexual couples (b) Heterosexual couples
20
03
00
40
05
00
60
0A
nn
ua
l la
bo
r e
arn
ing
s in
1,0
00
NO
K
−4 −3 −2 −1 0 1 2 3 4 5Age of first child
Mothers Co−mothers
(c) Lesbian couples (d) Lesbian couples
65
07
00
75
08
00
85
09
00
An
nu
al la
bo
r e
arn
ing
s in
1,0
00
NO
K
−4 −3 −2 −1 0 1 2 3 4 5Age of first child
Fathers Co−fathers
(e) Gay couples (f) Gay couples
Figure 5: Raw child penalties (left) and estimated child penalties (right) across couples types
Note: Left panels show means of annual labor earnings for the years before and after birth of the �rst child. Right
panels show the estimated child penalties from equation 3 for a) and b) heterosexual couples, c) and d) lesbian
couples and e) and f) gay couples. Samples sizes are 231,200 heterosexual couples, 535 lesbian couples and 29 gay
couples. Sample construction and data as de�ned in section 3. Bootstrapped 95% con�dence intervals in gray using
200 replications and clustering by couple. Note that the scale of the y-axes are separate for gay couples compared
to heterosexual and lesbian couples.
Figure 6: Partial child penalties, controlling for comparative advantage
types. Next, in Figure 6we report estimates conditional on household specialization correspond-
ing to equation 7. Note that this �gure represents the remaining child penalty after removing the
portion of the penalty explained by comparative advantage. If anything, the di�erences become
even more stark.
4.1 Robustness checks
One major assumption of the model is that η is identical for lesbian and heterosexual women. This
is a strong assumption. If η is larger for lesbian women, then the contribution of gender norms is
even larger. If η is smaller for lesbian women, then the results could be driven only by preferences,
and not be gender norms. This is an untestable prediction. However, if the average η is smaller
for lesbian women then for all heterosexual women, then we might also expect η to di�er among
di�erent groups of heterosexual women. Below we graph the event studies separately for high
educated and low educated women, and for high and low income women. [IN PROGRESS].
4.2 Overall impact on household income
The child penalty experienced by women in heterosexual couples is so large, it would seem to
imply an overall household income penalty. In Figure 7 we show this is the case. Moreover, we
show that the household income penalty experienced by lesbian couples is much smaller in later
years. We exclude gay couples from this analysis due to the small sample size of gay couples,
26
Figure 7: Child penalty, total household income
but as you would expect based on the previous �gures, gay couples experience even smaller
household income penalties compared to lesbian and heterosexual couples.
4.3 Child outcomes
We have shown that individuals in same sex couples share the burden of child rearing much more
evenly, and experience less severe household income penalties compared to heterosexual couples.
However, this approach may not be optimal from a social planner’s perspective if the reduction in
the relative child penalty comes at the cost of worse outcomes for children. If sharing the burden
of child care is simply more e�cient, then same sex couples and their children could be better o�
than heterosexual couples and their children. Alternatively, same sex couples could be choosing
to substitute purchased child care for home production, in which case their children could be
equally well o�. Last, same sex couples could be investing less in their children, in which case
their children would be worse o�. In Table 3 we present the test scores at age 10 for the children
of heterosexual and same sex couples. We �nd that the children of same sex couples perform
better on these tests, and the estimates are signi�cant at the 99th percentile for both reading and
27
English. These results suggest that while same sex parents appear to parent more equally and
experience smaller costs to overall household income, their alternative approach to child rearing
does not come at the cost of child outcomes.
5 The impact of family friendly policies
The results thus far suggest that the child penalty experienced by heterosexual couples is pri-
marily driven by female preferences and gender norms, and that the alternative shared parenting
approach taken by same sex couples increases household income and improves child outcomes.
Despite the persistence of the child penalty within heterosexual couples, history suggests that
decreases in the child penalty are possible. In Figure 8 we graph the child penalty of women and
men in heterosexual couples from 1980-2009. Note that each line represents the child penalty
for children born during a four year interval, estimated using the event study approach from the
previous sections (see equations 5 and 3).
The �gure shows that the child penalty for women has declined substantially over time. In
the 1970s and 1980s fathers not only didn’t experience a child penalty, but actually received an
increase in income as a result of having their �rst child. However, over time this child bonus for
fathers has decreased, and currently fathers largely experience no change in income following
the birth of their �rst child. Combining the two groups, while the reduction in the relative child
penalty has been substantial from the 1970s to the current day, the remaining gap is still large,
and largely driven by the penalties experienced by mothers. In the remainder of this paper we
estimate the impact of two di�erent policies on the relative child penalty: paid paternity leave
and improved access to formal child care. Paid paternity leave targets the father’s participation
in child rearing, while formal child care o�ers the state as a “third partner” to share the burden
of child rearing with mothers.
5.1 Paternity leave
As means for increasing fathers’ involvement in raising children, the so called daddy quotas
of the Scandinavian countries have attracted considerable interest. Starting as early as 1992,
28
29
Table 3: Impact on the children: Test scores at age 10
Math Reading English
Female child -0.106*** 0.154*** -0.0252***
(0.00342) (0.00344) (0.00353)
Same sex parents 0.105 0.280*** 0.209***
(0.0834) (0.0761) (0.0808)
Controls
Age (mother × father) X X X
Education level (mother × father) X X X
Pre-birth income (mother, father, interacted) X X X
Year X X X
Observations 303,490 302,468 302,670
Children of lesbian couples 134 133 133
Children of gay couples 4 4 4
Note: Cross sectional regressions of test scores on couple types, controlling as indicated. Sample consist
of all children born 2001-2007 in the main sample described in Section 3, before conditioning on the �rst
child or the age of the parents at �rst birth. Standard errors in parentheses are clustered at mother and
father using two-way clustering. Test scores are normalized within course and year to have mean zero and
standard deviation 1.
30
−.5
−.4
−.3
−.2
−.1
0.1
.2re
lative c
hild
penaltie
s in e
arn
ings
−5 0 5 10 15 20child age
Mothers
−.5
−.4
−.3
−.2
−.1
0.1
.2re
lative c
hild
penaltie
s in e
arn
ings
−5 0 5 10 15 20child age
Fathers
1971−1975 1976−1980 1981−1985
1986−1990 1991−1995 1996−2000
2001−2005 2006−2010
Birth cohort, first child
Figure 8: The relative child penalty in income over time for mothers and fathers in heterosexual
couples
Norway mandated a four week period of parental leave for fathers. This leave period could not be
transferred to the mother. A number of other countries have introduced similar quotas, including
Ireland (14 weeks), Slovenia and Iceland (13 weeks), Germany (8 weeks), Finland (7 weeks), and
Portugal (6 weeks) (see OECD (2014)). Paternity leave, by forcing fathers to spend more time
with their children, might increase the value fathers place on time with children (increasing β)
and might also decrease the distaste fathers have for mothers working outside the home (reducing
α). Paternity leave could also increase the productivity of fathers in home production (increasing
ka). Within the framework of our model, all of these e�ects would decrease the relative child
penalty.
A number of papers have estimated the impact of paternity leave policies on di�erent out-
comes.12
A few particularly relevant ones include (Cools et al., 2015; Kotsadam and Finseraas,
2013) who �nd positive impacts of the Norwegian paternity leave policies on child outcomes
looking at the 1993 reform. Dahl et al. (2014) �nd substantial peer e�ects of the Norwegian pol-
icy in 1993 using a regression discontinuity approach. Rege and Solli (2013) �nd a decrease in
father earnings long term in Norway from the 1993 reform using a di�erence in di�erence ap-
proach and Johansson (2010) �nds that a Swedish policy increases mother’s earnings but has no
impact on fathers. Ekberg et al. (2013) �nd that fathers are no more likely to take sick leave to care
for a sick child long term using a Swedish reform, and Patnaik (2014) �nds a large and persistent
change in the division of household labor from a Canadian daddy quota. This selection of papers
from a broader literature captures the fact that the existing literature �nds either no impact or
positive impacts on children. The literature �nds either no impact or a decrease in fathers income
and an increase in mothers income.
We add to this literature by looking speci�cally at the impact of paternity leave on the child
penalty in the context of our event study design from the �rst half. In Table 4 we report every
leave reform in Norway from 1992-2013. The maternal and paternal quota columns report the
amount of parental leave that is reserved exclusively for the mother and father. The remaining
leave can be shared among parents however they choose and is reported in column 6. Paid ma-
12An even larger literature looks at the impact of maternity leave on maternal earnings and child outcomes. See,
for example, Lalive and ZweimÃŒller (2009); Lalive et al. (2014); Carneiro et al. (2015); Baker and Milligan (2015).
31
Table 4: Parental leave reforms in Norway
Reform date Total Compensation Maternal quota Paternal Shared Max weeks
leave in weeks quota leave mother
(weeks) (weeks)
April 1st, 1992 35 (44.4) 100% (80%) 8 (2 before birth) 0 27 35
April 1st, 1993 42 (52) 100% (80%) 9 (3 before birth) 4 29 38
July 1st, 2005 43 (53) 100% (80%) 9 (3 before birth) 5 29 38
July 1st, 2006 44 (54) 100% (80%) 9 (3 before birth) 6 29 38
July 1st, 2009 46 (56) 100% (80%) 9 (3 before birth) 10 27 36
July 1st, 2011 47 (57) 100% (80%) 9 (3 before birth) 12 26 35
July 1st, 2013 49 (59) 100% (80%) 17 (3 before birth) 14 18 35
ternity leave is conditional on the mother working a su�cient amount and receiving a minimum
income in the months prior to giving birth (with some variation in the amounts across reforms).
For both parents to receive paid leave, both parents must work a minimum amount and receive a
minimum income in the months prior to birth. The reforms were generally announced in Octo-
ber the year before implementation as part of the budgeting process, making it nearly impossible
to plan conception in response to the announcement of the quota change to manipulate birth
dates around the cuto�. In the robustness checks Figure 12 we show that there is no statistically
signi�cant change in the density of births just before and just after the reform.
In this paper, we estimate results using the 1993, 2005, 2006, 2009, 2011, and 2013 reforms.
Because we are looking at short term impacts of children, we use the same regression disconti-
nuity design as Dahl et al. (2014). As in all regression discontinuity designs, identi�cation relies
on continuity in the underlying regression functions. Our identi�cation strategy exploits the fact
that parents of children born just before the reforms were not subject to the changes in parental
leave quotas, while parents of children born right after each reform were subject to the changes.
For this exercise, we draw on heterosexual couples from the main sample with �rst children
born in 2005, 2006, 2009, 2011 and 2013, and supplement this with couples with �rst children born
32
in 1993. We further restrict the samples to births around the cuto� using the optimal bandwidth,
see below. We begin by estimating the impact of each reform separately. We estimate a fuzzy RD
separately for mothers and fathers using the following speci�cation:
yit =∑t6=−1
βt1(xi > 0) + f(xi) + εit
Li = γb1(xi > 0) + g(xi) + ηit
Where we regress earnings at event time t for a mother or father with a child born close to the re-
form in year b and leave takeoutLi on a dummy for the child being born after the reform date and
separate local linear polynomials f and g of the running variable on either side of the cuto� date.
We use the optimal bandwidth that minimizes the mean squared error of the RD estimate to de�ne
the sample, and a triangular weighting function in order to obtain local estimates around the cut-
o�. Because the reforms di�er in the increase of quota implemented,w e scale the �rst stage and
reduced form estimates to represent the impact of an additional week of quota so that the reforms
are comparable. We estimate and report robust bias-corrected con�dence intervals (see (Calonico
et al., 2014) and Calonico et al. (2018)) together with the conventional, heteroskedasticity-robust
con�dence intervals.13
For additional details see Cattaneo et al. (2018a,b)
We report �rst stage estimates for these speci�cations in Table 5. We see clear and signi�cant
e�ects of all reforms except for the 2006 reform, whether using robust bias-correcting inference
or conventional inference that only accounts for heteroskedasticity.
We next plot the reduced form and �rst stage estimates together for each of the �ve reforms
in Figure 9 Despite the strong �rst stages in the top panels discussed above, the reduced form
estimates are relatively �at for both mothers and fathers and we �nd no signi�cant di�erences
between couples where the father is exogenously exposed to greater paternity leave and cou-
ples who are not. These results imply that paternity leave does not cause fathers to parent more
13Many models in this section are estimated using the robust RD commands for Stata written by Matias D. Catta-
neo and coauthors, whom we owe thanks. These include rdrobust, rddensity, rdbwselect and others. These packages
are documented in Calonico et al. (2018) and Cattaneo et al. (2018d).
33
34
Reform year 2005 2006 2009 2011 2013 Pooled Stacked
RD estimate 0.908 0.609 0.978 1.106 0.543 1.195 0.899
conventional standard error 0.474 0.421 0.105 0.325 0.234 0.166 0.089
robust standard error 0.544 0.510 0.125 0.375 0.274 0.189
conventional p-value 0.0554 0.148 0.000 0.001 0.020 0.000 0.000
robust p-value 0.0441 0.279 0.000 0.001 0.076 0.000
Robust 95% CI 0.0288 -0.448 0.758 0.480 -0.0507 0.891
2.160 1.550 1.246 1.949 1.022 1.630
Optimal bandwidth 43.10 51.34 72.00 33.36 69.97 41.43
Obsevations 17,173 17,714 18,892 18,641 18,649 91,069 91,069
E�cient observations 4,316 5,355 7,704 3,709 7,588 22,292 28,672
Weights in pooled 0.185 0.195 0.205 0.205 0.211
Weights in stacked 0.151 0.187 0.269 0.129 0.265
Quota increase 1 1 4 2 2 1.75 2.20
Table 5: RDD �rst stage estimates
Note: Robust semiparametric sharp RD estimates of the e�ect of paternity leave reforms on paternity leave takeout
using optimal bandwidths, triangular kernel and local linear polynomials on either side of the cuto�. All estimates
are scaled to re�ect one week of quota increase. Stacked estimates are the stacked individual cuto�s, allowing
polynomials to vary over cuto�s and using the cuto�-speci�c bandwidths and weights, and using the quota in stead
of the treatment indicator to secure scaling. Conventional standard errors are heteroskedasticity-robust, but not
bias-corrected.
equally with mothers, at least not in such a way that mothers experience less severe child penal-
ties. Estimates are, however, very imprecisely estimated.
In order to move beyond these separate reforms and increase the precision of our estimates, we
next stack all the reforms from above. The common way of doing this in RD studies is to
recenter the running variable to be zero at the relevant cuto� for all individuals and run
semiparametric RD estimates in the pooled sample. We call this the pooled estimate, and report
the �rst stage speci�cation for this procedure in Table 5 above. This estimate, however, restricts
the functional form of the local linear polynomials to be the same for all cuto�s, potentially
increasing the approximation error and lowering the precision of our estimates. An alternative
and more straigthforward way to stack the estimates is to allow the local polynomials of the
running variable to vary by cuto� and use the cuto�-speci�c optimal bandwidths and kernel
weights from the individual speci�cations. Unfortunately, we cannot calculate bias-corrected
standard errors for this speci�cation, but we argue that the problem should be relatively minor.
First, notice that the di�erence between the conventional and the robust standard error estimate
for the pooled speci�cation is relatively small, indicating that the variance coming from the
approximation error is relatively small. Second, the approximation error should be smaller for
the stacked than the pooled speci�cation because we allow the local polynomials to di�er
between cuto�s. Nonetheless, inference from this speci�cation is only correct if the model is
well speci�ed, so that approximation error vanishes asymptotically. We test the robustness to
the functional form in the next section.
The last two rows of Table 5 reports the results from these two speci�cations. The pooled
estimate is - somewhat surprisingly - larger than any of the cuto�-speci�c estimates, indicating
more than a one week increase in leave use per week increase in the paternity leave quota.
Second, although the estimate is highly signi�cant, notice that the standard errors of the pooled
estimate are still larger than the most precisely estimated individual cuto�. In contrast, the
35
(a)
First
stag
e2005
(b)
First
stag
e2006
(c)
First
stag
e2009
(d
)First
stag
e2011
(e)
First
stag
e2013
(f)
Red
uced
fo
rm
,2005
(g
)R
ed
uced
fo
rm
,2006
(h
)R
ed
uced
fo
rm
,2009
(i)
Red
uced
fo
rm
,2011
(j)
Red
uced
fo
rm
,2013
Figu
re
9:
Ro
bu
st
RD
Destim
ates,p
atern
ity
leave
refo
rm
s
Note:
To
pp
an
els
sh
ow
bin
ned
plo
ts
ofth
ew
eek
so
fp
atern
ity
leave
again
stbirth
date
ofth
ech
ild
in
day
safter
th
erefo
rm
,overlaid
with
th
eestim
ated
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cal
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ear
po
ly
no
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Bo
tto
mp
an
els
sh
ow
ssh
arp
RD
estim
ates
of
th
eim
pact
of
an
ad
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nal
week
of
th
erefo
rm
so
nm
atern
al
an
dp
atern
al
in
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me
by
year,scaled
to
rep
resen
tth
ee�
ect
of
on
ew
eek
of
in
creased
patern
ity
leave
qu
ota.
Op
tim
alM
SE
-red
ucin
gban
dw
id
th
s,trian
gu
lar
kern
el
an
dlo
cal
lin
ear
po
ly
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mials
on
eith
er
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eo
fcu
to
�.
Co
n�
den
ce
in
tervals
are
ro
bu
st
an
dbias-co
rrected
.
36
stacked speci�cation delivers improved precision over any of the individual estimates, �nding a
more reasonable .9 weeks increase in leave use per week of quota increase.
Informed by this, we move to estimate fuzzy RD speci�cations of the impact of paternity leave
use on mothers’ and fathers’ subsequent labor supply using the pooled and stacked estimates
from above. For the stacked estimates, we revert to the cuto�-speci�c treatment indicators as
instruments because the fuzzy RD takes care of the scaling across reforms for us. This
speci�cation exactly reproduces the cuto�-speci�c �rst stage estimates and so is a natural way
to stack the reforms. The results from the stacked and pooled fuzzy RD estimates for mothers
and fathers are presented together with the �rst stage in Figure 10. The top panel illustrates
how the various reforms a�ected paternity leave takeout, mirroring the estimates from table 5.
The bottom two �gures presents the impacts on mothers and fathers yearly incomes over time.
The estimates are �at and centered at zero, con�rming the �ndings from before of little impact
of paternity leave use. The stacked estimates do, however, provide more precise estimates than
the results using separate reforms, particularly for mothers using the stacked speci�cation,
ruling out positive impacts larger than around 5,000 NOK per week of paternity leave use for all
years post-birth.
Last, to provide a sense of the potential percentage change in the child penalty, we re-scale
the �gures so that they-axis to represent the percentage of the child penalty, as calculated in the
�rst half of the paper. We present these results in Figure ??. While point estimates are as before
close to zero, the lower bound of the e�ect is still informative. If we take the maximum reduction
in the child penalty after age 1 we �nd that one week of paternity leave at most decrease the
mother’s child penalty by around 5%, and estimates are similar for all years after age 1. Similar
estimates for fathers are too imprecise to draw �rm conclusions, in part because the initial child
penalty is very close to zero.
The results in this subsection cover a variety of di�erent paternity leave expansions. Despite
the number of reforms we study and the strength of the �rst stage for many of the reforms,
we never �nd a statistically signi�cant impact of paternity leave on the child penalty. Based
37
on these results, we conclude that paternity leave does not appear to reduce the relative child
penalty. Given that this frequently suggested program targeting fathers does not appear to a�ect
the child penalty, we now turn to the alternative approach available to governments: directly
support mothers.
5.1.1 Robustness Checks
The critical assumption for the validity of our RD tests is that the population of couples around
the discontinuity are identical. In Table 6 we report estimates that show that on observables,
individuals around the cuto� are statistically indistinguishable from each other with only a few
exceptions.
Additionally, we can test for manipulation around the cuto�. If parents were able to manipu-
late either conception or birth at the cuto� in order to qualify for reforms, then we would expect
a statistically signi�cant change in the density of births around the cuto�. In Figure 12, we show
this is not the case.
5.2 Improved access to formal child care
[IN PROGRESS]
6 Conclusion
[IN PROGRESS]
38
39
(a) First stage estimates
(b) Mothers (c) Fathers
Figure 10: Pooled and stacked fuzzy RD estimates
Notes:
40
Figure 11: Scaled stacked fuzzy RD estimates, mothers
Note: Figure shows the stacked fuzzy RD estimates for mothers, scaled by the estimated child penalties
from the baseline so that the estimates can be interpteted as the relative increase or decrease in the child
penalty per week increase in paternity leave takeout.
41
Table 6: Sharp RD balancing tests
Variable Reform year 2005 2006 2009 2011 2013 Pooled Stacked
Father’s RD estimate 0.0893 -0.247 0.0229 -0.108 0.170 -0.00571 0.0256
age conventional s.e. 0.259 0.253 0.0786 0.158 0.159 0.0918 0.0436
robust s.e. 0.259 0.253 0.0786 0.158 0.159 0.0918
conventional p 0.687 0.247 0.727 0.412 0.204 0.941 0.556
robust p 0.584 0.277 0.850 0.402 0.199 0.821
Mother’s RD estimate 0.173 -0.0174 0.0442 -0.202 0.294 0.0816 0.0731
age conventional s.e. 0.342 0.297 0.0936 0.189 0.187 0.111 (0.0515)
robust s.e. 0.342 0.297 0.0936 0.189 0.187 0.111
conventional p 0.547 0.944 0.571 0.197 0.0600 0.378 0.156
robust p 0.506 0.973 0.671 0.294 0.103 0.441
Maternity RD estimate 2.050 -1.692 0.0702 0.00876 1.187 0.117 -0.0464
leave conventional s.e. 1.614 1.401 0.364 0.607 0.540 0.337 0.193
takeout robust s.e. 1.614 1.401 0.364 0.607 0.540 0.337
conventional p 0.135 0.157 0.825 0.986 0.0145 0.691 0.810
robust p 0.141 0.142 0.605 0.957 0.00979 0.506
Father’s RD estimate 0.178 -0.477 0.0242 -0.0137 0.00835 -0.0255 0.0137
years of conventional s.e. 0.214 0.215 0.0488 0.0963 0.104 0.0653 (0.0306
education robust s.e. 0.214 0.215 0.0488 0.0963 0.104 0.0653
conventional p 0.322 0.0101 0.552 0.865 0.923 0.645 0.655
robust p 0.490 0.0123 0.680 0.819 0.964 0.553
Mother’s RD estimate 0.00107 -0.516 0.0519 -0.0263 0.0797 -0.0140 0.0299
years of conventional s.e. 0.219 0.221 0.0532 0.105 0.0934 0.0626 0.0319
education robust s.e. 0.219 0.221 0.0532 0.105 0.0934 0.0626
conventional p 0.995 0.00772 0.241 0.762 0.314 0.789 0.349
robust p 0.898 0.00785 0.297 0.765 0.295 0.748
Father’s RD estimate -0.0125 0.0128 -0.00405 0.00191 -0.00413 -0.00252 -0.00264
education conventional s.e. 0.0134 0.0121 0.00289 0.00547 0.00761 0.00354 0.00204
missing robust s.e. 0.0134 0.0121 0.00289 0.00547 0.00761 0.00354
conventional p 0.273 0.199 0.0985 0.674 0.522 0.410 0.196
robust p 0.324 0.280 0.115 0.777 0.427 0.321
Mother’s RD estimate -0.0102 -0.00258 -0.00134 -0.00785 -0.00902 -0.00626 -0.00364
education conventional s.e. 0.0114 0.00960 0.00330 0.00525 0.00776 0.00333 0.00190
missing robust s.e. 0.0114 0.00960 0.00330 0.00525 0.00776 0.00333
conventional p 0.286 0.755 0.631 0.0773 0.176 0.0269 0.0554
robust p 0.366 0.584 0.743 0.0990 0.145 0.0354
Note: Robust semiparametric sharp RD estimates of the e�ect of paternity leave quotas on balancing variables using
optimal bandwidths, triangular kernel and local linear polynomials on either side of the cuto�. All estimates are
scaled to re�ect one week of quota increase. Stacked estimates are the stacked individual cuto�s, allowing poly-
nomials to vary over cuto�s and using the cuto�-speci�c bandwidths and weights, and using the quota instead
of the treatment indicator to secure scaling. Conventional standard errors are heteroskedasticity-robust, but not
bias-corrected.
42
(a) 2005, p = 0.640 (b) 2006, p = 0.750
(c) 2009, p = 0.662 (d) 2011, p = 0.783
(e) 2013, p = 0.635 (f) All reforms, p = 0.536
Figure 12: Density plots below and above cuto�s
Notes: Graphs show density estimates above and below the cuto� using methods described in
Matias D. Cattaneo and Ma (2017) and implemented in Cattaneo et al. (2018c). p-values reported
are for a bias-corrected test of whether the densities at the cuto�s are equal.
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A Additional results
46
47
(a) Heterosexual couples
(b) Lesbian couples
(c) Heterosexual couples
Figure 13: Event studies with no age and year controls